Oral Ondansetron Versus Transdermal Granisetron (Sancuso) for Women With Cervical, Endometrial or Vaginal Cancer Receiving Pelvic Chemoradiation: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Oral Ondansetron Versus Transdermal Granisetron (Sancuso) for Women With Cervical, Endometrial or Vaginal Cancer Receiving Pelvic Chemoradiation (NCT01536392), a randomized phase 3 study. The primary outcome is Percentage of Participants With Response Rate to Anti-Emetic Therapy Days 4-7 Each Chemotherapy Cycle.

2. Clinical Question

The study’s stated purpose was to compare granisetron delivered by patch with ondansetron taken by mouth for reducing nausea and vomiting in women receiving chemoradiation. The clinical question therefore concerns both a difference in treatment delivery and the response measure during chemotherapy cycles. The primary response definition is specific: a participant had to have no emetic or retching episodes and no rescue medication use during days 4-7 after chemotherapy. It does not, by itself, summarize every aspect of nausea, vomiting, adherence or quality of life that the registry describes as measured.

The registry also identifies a secondary response outcome for the period from chemotherapy through 24 hours. This is a different time window from the primary late-onset period. The distinction matters because a response percentage for one period cannot be assumed to describe the other period. The record reports the same numeric results for both outcomes, a point that warrants care when interpreting their relationship. The clinical question is comparative, but the posted information primarily supports a descriptive reading of responses in the two groups rather than a definitive conclusion about relative effects.

3. Trial Design

The registry classifies NCT01536392 as a phase 3, randomized, parallel-group trial with no masking. M.D. Anderson Cancer Center is listed as the sponsor. The trial status is completed, and the registry reports enrollment of 76. The listed start is 2012-03 and primary completion is 2019-10-03. These record details describe the trial’s structure and timeline; they do not explain how the allocation sequence was generated or concealed, because those methods are not reported in the registry record.

The two groups received different antiemetic regimens. The transdermal granisetron arm used a 34.3 mg patch replaced every 7 days, with patch placement or replacement before intravenous cisplatin. At cycle 1, participants also received intravenous granisetron before cisplatin and before the patch. The oral ondansetron arm used 8 mg thrice daily beginning with cisplatin administration and continuing for 72 hours after the infusion. The groups therefore differed in both medication and route of administration. The registry does not report enough detail to assess whether other aspects of care were standardized between groups.

The registry lists questionnaires and a study drug diary as behavioral interventions, alongside granisetron and ondansetron as drugs. It describes assessment of adherence, nausea and emesis, pill counts or compliance, and quality of life. The primary outcome was assessed each cycle through 5 cycles, with the timeframe described as an average of 6 weeks. The endpoint description includes several measurement instruments, but it does not provide a detailed account of how each was integrated into the primary response calculation beyond the stated requirement for no emetic or retching episodes and no rescue medication use.

Posted outcome denominators are 41 for transdermal granisetron and 34 for oral ondansetron. Those denominators do not sum to the registry’s enrollment of 76. The reason for the difference is not reported in the registry record. It is therefore important to distinguish enrollment from the denominators attached to the posted outcome results rather than assume that every enrolled participant contributed to each outcome.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: 76 participants signed consent, 1 participant did not receive treatment due to the study closure.

Overall Study

Reasons for not completing this period:

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With Response Rate to Anti-Emetic Therapy Days 4-7 Each Chemotherapy Cycle, measured over Baseline, up to 7 days post-chemotherapy, through 5 cycles of chemotherapy measured each cycle, an average of 6 weeks.

The primary endpoint is the percentage of participants with a response to anti-emetic therapy during days 4-7 after each chemotherapy cycle. A response was defined as having no emetic or retching episodes and no rescue medication use during that late-onset phase. The registry describes measurement at baseline and up to 7 days after chemotherapy, across 5 chemotherapy cycles, with an average timeframe of 6 weeks.

This kind of endpoint reduces a complex experience to a clearly specified participant-level response: whether both stated conditions were met during the assessment period. That makes the percentage interpretable as the share of participants meeting the operational definition, rather than as an average symptom score. It is also clinically relevant to the stated study objective of comparing approaches to reducing nausea and vomiting during chemoradiation. However, the binary response does not convey how severe or frequent symptoms were among participants who did not meet the response definition, nor does it distinguish which part of the definition was unmet.

The record also describes the Osoba Nausea and Emesis Module as a quality-of-life measure, with higher scores indicating worse quality of life, and the Morisky Medication Adherence Scale, with higher scores indicating higher compliance. The registry gives the adherence scale’s scoring description, but the primary response remains defined by symptoms and rescue medication use. The response percentages should not be treated as interchangeable with those separate measures.

7. Results Posted in the Registry

• Arm 2: Oral Ondansetron: 38.2% (13/34) versus 48.8% (20/41) on control; risk difference -10.5 percentage points (95% CI -32.9 to 11.8), risk ratio 0.78 (0.46–1.33); unadjusted two-proportion z-test p = 0.360.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Percentage of Participants With Response Rate to Anti Emetic Therapy 0-24 Hours Each Chemotherapy Cycle

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Arm 2: Oral Ondansetron: 38.2% (13/34) versus 48.8% (20/41) on control; risk difference -10.5 percentage points (95% CI -32.9 to 11.8), risk ratio 0.78 (0.46–1.33); unadjusted two-proportion z-test p = 0.360.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm 2: Oral Ondansetron and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists a secondary response outcome for the period from chemotherapy through 24 hours, while the primary outcome concerns days 4-7 after chemotherapy. The two outcomes address different time windows within the broader nausea and vomiting question. In principle, an early response measure could complement a late-onset measure by describing another part of the post-chemotherapy course. However, the posted results for the secondary outcome are numerically identical to those for the primary outcome, including the group percentages, confidence intervals, counts and comparative estimates. The registry does not explain why the results are identical.

Because the secondary and primary windows differ, identical posted estimates should not be treated as independent confirmation that the treatment contrast is consistent over time. Nor should the secondary result be used to amplify the primary finding without knowing how the data were constructed or summarized for each interval. The record gives no reported analysis entries describing how these repeated outcome periods were analyzed, whether the periods were evaluated separately, or how cycle-level data contributed to the results.

Secondary outcomes generally carry less evidential weight than a prespecified primary outcome when their analysis methods and role in the study are not fully reported. If many outcomes or time windows are examined, the chance of finding an apparently notable result by chance can increase. Statistical adjustment or a prespecified hierarchy can address some multiplicity concerns, but the registry record does not report such a plan. The unadjusted secondary result should therefore be considered exploratory in interpretation, not a separate definitive test of the treatment comparison.

The registry describes additional measurements related to adherence and quality of life, including Morisky Medication Adherence and the Osoba Nausea and Emesis Module. It provides scale interpretation but no posted results for those measures in the outcome information. Their presence in the measurement description does not establish that one group had better adherence or quality of life. Overall, the secondary information adds a stated assessment window and measurement context, but the record’s numerical duplication and lack of analysis detail limit its ability to provide independent support for the primary result.

Secondary outcomes registered for this trial, for reference (only those above were recalculated):

• Percentage of Participants With Response Rate to Anti Emetic Therapy 0-24 Hours Each Chemotherapy Cycle

9. Statistical Interpretation

10. Statistical Methods Explained

The registry describes a randomized, parallel-group trial with no masking. Randomization is a general method for assigning participants to groups so that, on average, measured and unmeasured characteristics are less likely to determine treatment assignment. It can strengthen the basis for comparing outcomes, but it does not guarantee balanced groups in a trial of limited size. The registry does not report how the sequence was generated, whether assignments were concealed before enrollment, or what characteristics were used to assess group comparability. Those design details are therefore not reported in the registry record.

What does the response percentage represent?

The primary outcome is a binary response: each participant either meets the registry’s definition or does not. Meeting the definition required no emetic or retching episodes and no rescue medication use during days 4-7 after chemotherapy. The group percentage describes the proportion meeting that definition among the participants represented by the posted denominator. This is not a measure of average symptom intensity. Participants who fail to meet the definition may differ substantially in the symptoms or rescue medication use that led to nonresponse, but the posted binary result does not show those distinctions.

The registry states that response was measured each chemotherapy cycle, through 5 cycles. Repeated measurements on the same participant are generally related: a participant’s response in one cycle may be associated with that participant’s response in another. General statistical methods for repeated outcomes account for that within-participant relationship. The registry record does not report whether the posted results combine cycle-specific responses, summarize participants across cycles, or use a repeated-measures model. Nor does it report a method for handling participants with incomplete cycle data. This means the percentage should be interpreted according to the stated endpoint description, without assuming a particular repeated-measures method.

How should the comparison be understood?

The risk difference is a comparison of the response probability in one group with the response probability in the other, expressed on an absolute scale. The posted estimate is -0.105 for oral ondansetron relative to transdermal granisetron. The negative sign indicates the direction of the estimate under that group ordering; it does not indicate how certain the estimate is. The confidence interval from -0.329 to 0.118 gives the range of effects compatible with the data under the method used to calculate it. Because the interval includes zero, the data are compatible with no risk difference as well as effects in either direction.

The record also posts a risk ratio of 0.784, with an interval from 0.461 to 1.332, and an odds ratio of 0.65, with an interval from 0.258 to 1.637. These are alternative relative-effect scales. A risk ratio compares response probabilities as a ratio, while an odds ratio compares the odds of response. Relative measures can look different from an absolute risk difference because they use different scales. The confidence intervals for these measures also span the value representing no relative difference. These measures should not be treated as independent confirmations: they are alternative descriptions of the same group results.

The posted unadjusted p-value is 0.36. A p-value measures, under a specified null model and analysis assumptions, how unusual the observed data or more extreme data would be if the null hypothesis were true. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The registry does not state a planned significance threshold or provide a complete statistical analysis plan. Accordingly, the p-value should be read as an unadjusted result rather than evidence about a prespecified decision rule that is not reported.

What can confidence intervals add?

A confidence interval communicates uncertainty around an estimate. In general, a narrower interval indicates greater precision under the method’s assumptions, while a wider interval leaves more uncertainty about the range of plausible effects. The posted intervals are wide enough to include materially different possibilities, including no difference. An interval is not a guarantee that the true effect lies within its endpoints, and its interpretation depends on the statistical method and assumptions. The record identifies the intervals as 95% confidence intervals but does not report the calculation method in detail.

For a binary outcome, different interval methods can behave differently, especially when samples are limited or response probabilities are near the boundaries of the possible range. The registry does not identify which method was used for the posted group percentages or comparative interval. No alternative analysis is reported to show how sensitive the results are to the choice of method. The safest reading is therefore to treat the posted estimates and intervals as the registry’s reported analysis rather than infer an unreported calculation procedure.

What do the analysis listings tell readers?

The record lists no reported analyses, even though posted outcome comparisons include an unadjusted p-value and effect estimates. This distinction means the record does not give a formal analysis listing that explains the methods, population or model behind those comparisons. It also does not report adjusted analyses. The absence of that detail makes it difficult to determine whether the comparison reflects all randomized participants, participants with available outcomes, or another analysis population. The denominators attached to the outcome results are the information available for interpreting the posted estimates.

The registry describes questionnaires, a study drug diary, adherence measures and quality-of-life measurement. These measures can provide context beyond the binary response, but the registry does not post analysis results for those details in the primary result information. It would be inappropriate to infer unreported findings from the description of planned or collected measurements. The response estimate remains one endpoint, not a complete representation of symptom burden, adherence or quality of life.

11. Confidence Intervals and Precision

The primary response estimate for transdermal granisetron is 49.8%, with a 95% confidence interval from 35.2% to 64.3%. For oral ondansetron, the estimate is 39.7%, with a 95% confidence interval from 24.4% to 56.1%. These intervals show substantial uncertainty around each group’s response percentage. The interval for oral ondansetron extends from a lower response percentage to a higher one, and the two group intervals overlap. The estimates therefore do not pin down a narrow range of possible group response patterns.

For the risk difference comparing oral ondansetron with transdermal granisetron, the estimate is -0.105 and the 95% confidence interval is -0.329 to 0.118. This interval includes zero, meaning the posted data are compatible with no difference, and it extends to values on both sides of zero. The interval is more informative than the point estimate alone because it makes the uncertainty and directionally mixed possibilities explicit. It does not establish equivalence: demonstrating equivalence would require a prespecified margin and an analysis designed to test that question, neither of which is reported in the registry record.

Confidence intervals are general measures of uncertainty, not direct probabilities that a particular effect is true. Their width depends on the amount of information in the data and on the statistical method. The denominators of 41 and 34 indicate the participant counts attached to the posted groups, while the registry’s enrollment is 76. The reason these figures differ is not reported in the registry record. Without a fuller account of missing outcomes and analysis populations, the precision estimates cannot be assessed against a complete participant flow.

The record also posts intervals for the relative measures, but each uses the same underlying outcome data and does not add independent information. A concise interpretation is that the observed estimates favor different response levels in the two groups depending on scale and direction, while the intervals remain compatible with no difference and with effects in either direction. The posted results are therefore imprecise for deciding how large or which-direction the comparative effect may be.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The sample-size figures are planning illustrations derived from the observed effect, not the original trial’s documented design assumptions. They assume a two-sided significance level of 0.05, equal allocation between the two arms and a normal approximation. The effect to detect is set as the stated fraction of the observed effect. The original sample-size justification and its assumptions are not reported in the registry record.

The figures are participants per arm, not total participants and not total events. For planning at 100% of the observed effect, the illustration gives 346 participants per arm for 80% power and 463 participants per arm for 90% power. At 75% of the observed effect, it gives 620 participants per arm for 80% power and 829 participants per arm for 90% power. At 50% of the observed effect, it gives 1,403 participants per arm for 80% power and 1,877 participants per arm for 90% power.

Power is the chance, under the specified assumptions and a particular true effect, that a planned study would detect an effect according to its testing rule. The 80% column represents a design targeting 80% power under the illustration’s assumptions; the 90% column targets 90% power. Higher target power requires more participants when the other assumptions are held fixed. The rows also illustrate that smaller effects need more participants to detect: the smaller the fraction of the observed effect being targeted, the larger the listed sample size. This is not observed power. It is a planning calculation based on the observed effect and should not be read as a retrospective measure of whether the completed trial had adequate power.

The curve associated with such planning calculations is a visual way to relate assumed effect size to required sample size under the stated assumptions. It cannot show what the trial’s original investigators planned unless those original assumptions are reported. These figures also depend on assumptions such as equal allocation and the normal approximation; changing assumptions can change the planning result. The record does not report the original sample-size rationale, a target enrollment based on that rationale, or whether the trial’s recruitment goal changed.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.488; treatment proportion p₁ = 0.382; average p̄ = 0.435.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7011 = 1.3742.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6971 = 0.5867.
4. n = (1.3742 + 0.5867)² / (-0.1055)² = 345.8, rounded up to 346 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
p0 <- 0.48780487804878                          # control proportion
p1 <- 0.382352941176471                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(1536392)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 346 (80% power), 463 (90% power)
 75% of observed effect: n per arm = 620 (80% power), 829 (90% power)
 50% of observed effect: n per arm = 1,403 (80% power), 1,877 (90% power)
power.prop.test: 345.8 
Simulated power at n = 346 per arm: 0.802 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary endpoint and a secondary response endpoint, and describes additional measures of medication adherence, nausea and emesis, pill counts or compliance, and quality of life. Examining more than one outcome, time window or cycle creates a multiplicity issue: the more comparisons considered, the greater the chance that at least one may appear notable by chance. A prespecified plan can identify which outcome is primary, define how secondary outcomes will be interpreted and specify whether statistical adjustments will be used. Such a plan is not reported in the registry record.

The posted comparison includes an unadjusted p-value of 0.36. The record does not report a multiplicity adjustment, a testing hierarchy, or a planned significance threshold. It is therefore not possible to determine whether the posted p-value was intended as a formal confirmatory test, how it relates to other comparisons, or whether any adjustment was applied elsewhere. The absence of reported analyses makes these questions particularly important; it does not justify assuming that no analyses were conducted, only that their details are not reported in the registry record.

Missing-data handling is also not reported. The registry reports enrollment of 76 and outcome denominators of 41 and 34, but gives no participant flow explaining the difference. It does not say how many participants discontinued, missed a cycle, lacked an endpoint assessment or were excluded from the posted result. It also does not describe imputation, complete-case analysis, sensitivity analysis or another approach to incomplete outcomes. Without that information, the influence of missing observations on the response percentages cannot be evaluated.

The analysis population is not reported. The record does not specify whether results follow an intention-to-treat principle, include all randomized participants, or use another population. It also does not state how the repeated cycle measurements were combined or modeled. These omissions limit assessment of how closely the posted estimates preserve the protection of randomization and how robust they are to incomplete observations. The appropriate conclusion is that the registry record leaves multiplicity, missing-data procedures and analysis-population definitions unresolved.

15. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 3% reporting threshold.

Most frequent non-serious adverse event terms

The registry reports no serious adverse events affecting participants in either group: 0 among 41 participants in the transdermal granisetron arm and 0 among 34 in the oral ondansetron arm. It also reports 0 deaths in each group. These counts describe the safety information posted in the registry; they do not establish that no serious events occurred outside the reporting definitions or observation period, details of which are not reported in the registry record.

Other adverse events are reported as affecting 15 of 41 participants in the transdermal granisetron group and 12 of 34 in the oral ondansetron group. The record does not provide the event terms or severity breakdown in the adverse-event information, so these counts do not reveal what kinds of events were involved, how often events occurred per participant, or whether events were considered related to treatment. A count of affected participants is not the same as a count of individual events.

Safety counts should be interpreted alongside the size of the groups and the limited detail posted. Zero reported serious adverse events is a descriptive finding in this trial record, not proof that a serious risk is absent. Likewise, the non-serious adverse-event counts should not be used alone to compare overall safety without event types, definitions, follow-up duration and analysis details.

16. What the Result Does, and Does Not, Mean

The posted results describe the proportion of participants meeting a specific late-onset response definition in each treatment group, together with uncertainty intervals and a comparative estimate. The response percentages are higher in the transdermal granisetron group than in the oral ondansetron group as reported, while the risk-difference interval includes zero and extends in both directions. The data therefore do not establish a clear difference between the groups. They also do not establish that the regimens are equivalent or that their effects are interchangeable.

The result applies to the defined response measure: no emetic or retching episodes and no rescue medication use during days 4-7 after chemotherapy. It does not capture every dimension of nausea, vomiting, adherence or quality of life. The record describes additional measurement instruments but does not post their corresponding results in the outcome information. The response percentages should not be generalized to unreported outcomes or interpreted as a complete account of treatment experience.

The registry describes women with cervical, endometrial or vaginal cancer receiving pelvic chemoradiation, but the posted information does not provide further population characteristics that would allow detailed assessment of how representative the participants were. The registry’s condition list specifically names cancer of the cervix, while its title and study summary include the other cancer types. The outcome denominators are 41 and 34, and the reason they differ from total enrollment of 76 is not reported. The trial is unmasked, and methods for randomization, missing data and analysis populations are not described.

Accordingly, the findings are best read as an uncertain descriptive comparison in the participants represented by the posted results. The record does not support a broad conclusion about all people receiving chemoradiation, other treatment schedules or outcomes beyond those reported. It also does not justify medical advice. The statistical message is limited: the point estimates differ, but the available precision and incomplete reporting leave substantial uncertainty about the size and direction of any underlying comparative effect.

17. Why This Trial Matters Statistically

This trial raises a useful statistical question about how to compare two treatment regimens when the endpoint is a binary response measured repeatedly across chemotherapy cycles. The response definition is concrete and tied to both symptoms and rescue medication use. At the same time, its binary form compresses a potentially varied experience into a yes-or-no outcome. Reporting the group percentages with confidence intervals helps readers see both the observed response levels and the uncertainty around them.

The contrast also illustrates why a point estimate should not be read in isolation. The posted estimate favors one direction, but its confidence interval includes zero and spans effects in the opposite direction. A p-value alone would not communicate that range of plausible effects. Reporting absolute and relative measures can add context, though those measures are alternative descriptions of the same data rather than independent findings.

Repeated assessment creates another important issue. Outcomes observed across cycles from the same participant are generally correlated, so the choice of summary and analysis method matters. The registry says measurements occurred through 5 cycles but does not report how the repeated observations were handled. This limits assessment of whether the posted percentages represent cycle-level summaries, participant-level response or another aggregation.

The record also demonstrates the value of complete reporting. Enrollment, outcome denominators, analysis populations, missing-data procedures, multiplicity plans and the original sample-size rationale are all relevant to interpreting a randomized trial. Several are not reported in the registry record. The secondary endpoint’s identical posted values despite a different time window further emphasizes the importance of transparent outcome-specific reporting. These limitations do not erase the descriptive information, but they define how far statistical conclusions can responsibly extend.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

Several trial-specific limitations constrain interpretation. The registry classifies the study as unmasked. For an outcome involving symptoms and rescue medication use, lack of masking may matter to participant reporting, treatment expectations or decisions about rescue medication. The record does not describe safeguards or procedures that would allow those possibilities to be assessed. This is a concern for interpretation, not evidence that the posted responses were biased.

The registry reports randomized allocation but does not describe sequence generation or allocation concealment. It also does not give baseline participant characteristics, so the balance of the groups on measured prognostic features cannot be reviewed from the posted information. Enrollment is 76, while the outcome denominators are 41 and 34; participant flow and reasons for the difference are not reported. Missing-data handling and the analysis population are also not reported, limiting evaluation of possible attrition effects.

The endpoint description refers to responses measured each cycle through 5 cycles, but the analysis approach for repeated observations is not stated. The registry does not explain whether the primary response result is a participant-level summary or a cycle-level summary. No adjusted analysis or detailed statistical analysis plan is reported. The secondary outcome uses a different time window yet has numerically identical posted results, and the reason is not reported in the registry record.

Further limitations include the lack of posted detail on event types for other adverse events, and the absence of results for the described adherence and quality-of-life measurements in the outcome information. The original sample-size justification is not reported; the posted planning illustration is based on the observed effect and cannot establish what the trial was designed to detect. These reporting gaps mean that the result can be described, but its robustness, generalizability and relation to the original analytic intentions remain uncertain.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Oral Ondansetron Versus Transdermal Granisetron (Sancuso) for Women With Cervical, Endometrial or Vaginal Cancer Receiving Pelvic Chemoradiation — NCT01536392.
• Registry record last updated 2021-06-11; status last verified 2021-05.
• Results first posted 2021-05-17.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

NCT01536392 is a completed, randomized, open-label, parallel-group phase 3 trial sponsored by M.D. Anderson Cancer Center. It compared a transdermal granisetron regimen with oral ondansetron in women receiving pelvic chemoradiation for cervical, endometrial or vaginal cancer. The registry reports enrollment of 76 and primary completion on 2019-10-03.

The primary outcome was response during days 4-7 after chemotherapy, defined as no emetic or retching episodes and no rescue medication use. The posted group percentages were 49.8% for transdermal granisetron and 39.7% for oral ondansetron; the risk-difference estimate was -0.105, with a 95% confidence interval from -0.329 to 0.118 and an unadjusted p-value of 0.36. The interval includes zero, and the posted comparison is uncertain.

The registry also lists an early response outcome, but its posted numerical results are identical to the primary outcome despite the different assessment window. The reason is not reported. Analysis methods, missing-data handling, analysis populations and the original sample-size rationale are not reported in the registry record. Serious adverse events and deaths are recorded as 0 in both groups; other adverse events affected 15 participants in the granisetron group and 12 in the ondansetron group.